Deconstructing the modular organization and real-time dynamics of mammalian spinal locomotor networks

Locomotion empowers animals to move. Locomotor-initiating signals from the brain are funneled through descending neurons in the brainstem that act directly on spinal locomotor circuits. Little is known in mammals about which spinal circuits are targeted by the command and how this command is transformed into rhythmicity in the cord. Here we address these questions leveraging a mouse brainstem-spinal cord preparation from either sex that allows locating the locomotor command neurons with simultaneous Ca2+ imaging of spinal neurons. We show that a restricted brainstem area – encompassing the lateral paragigantocellular nucleus (LPGi) and caudal ventrolateral reticular nucleus (CVL) – contains glutamatergic neurons which directly initiate locomotion. Ca2+ imaging captures the direct LPGi/CVL locomotor initiating command in the spinal cord and visualizes spinal glutamatergic modules that execute the descending command and its transformation into rhythmic locomotor activity. Inhibitory spinal networks are recruited in a distinctly different pattern. Our study uncovers the principal logic of how spinal circuits implement the locomotor command using a distinct modular organization.

1) Spinal cord and brainstem sectioning: how were the cut performed? Vibratome? Blade? Also, when moving through more caudal brainstem section, was the sequential cuts performed on the same preparation?
2) Could the authors give a little more details on how the cu sections (both brainstem and spinal cord) were held in a horizontal plane in order to allow visualization and imaging of the tissue?
3) CTB injection: was the injection performed between vertebrae (without laminectomy)? Do the authors have an estimate of the site of injection in the L2 segment? Was it ventral or dorsal? 4) Line 592, tip diameter was 70 micron, not mm 5) Line 616: CTB conjugated with? Biotin? Alexa? 6) Please define oscillatory index: is it the peak to trough distance in the correlation coefficient? Also, please define the exact formula of the auto-correlation coefficient, because from plot 5c it looks like it is defined between [-1,1] Minor Line 112 Should be 'corresponds to' rather than 'corresponding to' Line 169 'serotoninergic neurons do not initiate locomotion' and I would add 'nor modulate it', as shown in Suppl. 3b, that is quite interesting (and to me, a bit unexpected) Reviewer #2 (Remarks to the Author): General Comments: This manuscript describes an interesting and elegant description of the spatiotemporal organization of spinal modules involved in the transformation of tonic drive from descending regions of the brainstem into rhythmic activity in the spinal locomotor network. Overall, the work was received with enthusiasm, and it provides a roadmap for future work. Some weaknesses were identified, including a better rationale for unilateral stimulation and lack of control experiments related to electrical microstimulation, that, if addressed, will strengthen the manuscript.
Major Comments: • The rationale for using unilateral stimulation is lacking and needs to be better articulated.
• Line 8: The use of the term "whole brain screening" is misleading and implies that more areas were examined than what was reported. A more accurate statement is "whole brainstem screening".
• Lines 70-71: There is a lack of control experiments to support the authors assertion that lower intensity microelectrical stimulation (mES) restricts activation of smaller regions of the brainstem than does broader, more intense stimulation. Although this assertion is reasonable and likely, control experiments supporting this are suggested. Simply, one could express GCaMP6f in a pan-neuronal transgenic line and monitor/measure the spread of calcium signals with different stimulation parameters in the presence of TTX to abolish fast synapses. One predicts that the lower intensity mES will activate and spread across a smaller/more restricted region of the transverse cord. For example, mES of serotonergic region of transverse brainstem produced rhythmic spinal locomotor activity (Fig.  2h), which suggests that mES is not as restrictive as implied. Thus, there is not sufficient evidence to support the statement that mES is confined to the LPGi/CVL region (lines 179-82).
Minor Comments: • Title: Grammatically incorrect and suggest either "Deconstruction of the modular…" or "Deconstructing the modular…".
• Lines 122-23: The callouts to Fig. 1n for the left and right panels are reversed (left -time-frequency plot; right -circular plot).
• Lines 156-57 and Fig. 2: Panel e shows (labeled) colocalization of TPH and CTB, while panel f shows (labeled as) colocalization of Vglut2 and CBT, so it is necessary to confirm which subpanel goes with which callout.
• Lines 275-77: Please edit the sentence to reflect that calcium signal was monitored in spinal neurons but not in the ventral roots (as it is written). Extracellular recordings monitored activity in ventral roots.
• Line 336: Suggest to callout to Figure 3e regarding IEMi being the first rhythmic module.
• Lines 345-47: Provide the number of preparations that showed calcium signal in the ipsilateral lateral funiculus in response to LPGi/CVL stimulation in KA and mephenesin.
• Lines 347-49: Provide the number of preparations that showed calcium signal in neurons close to the central canal in in response to LPGi/CVL stimulation in mephenesin. Figure 1: The sagittal cuts located at 12N in Fig. 1 are listed as "12NR" and "12NC", whereas the same cuts in Supp. Fig. 1 are listed as "12-1" and "12N-2". So, the reader must assume which cuts are analogous in the two figures… please clarify.

• Figures 1 and Supplementary
Reviewer #3 (Remarks to the Author): In this manuscript, Hsu et al describe their work outlining a descending locomotor command from a specific brain stem reticulospinal area, the CVL/LPGi, to the mid-lumbar spinal cord, where the tonic descending signal is converted to a rhythmic signal to produce locomotor-like activity. They are addressing an important question -one that will be of great interest to the community studying locomotion. In addition, they use a broad range of techniques, and demonstrate the use of those techniques to understand connectivity between distant regions of the nervous system. Furthermore, the study is well organised and logical, and beautifully illustrated. As such, I am very enthusiastic about it.
Nonetheless, I have a few major concerns. I hope the authors read this in light of my enthusiasm and don't get discouraged by the length or number of my comments!
The manuscript is looking at the initiation of locomotion in the neonatal mouse over space and time.
There are issues about both that the authors should consider addressing: 1. Space: The authors are looking at a single segment in the lumbar spinal cord, L3/4. It is not clear why they selected this segment, and how the results would have differed, and the implications of those differences, had they looked elsewhere. For example, in the senior author's earlier work in the neonatal rat, the suggestion was made that the key region was in the more rostral lumbar spinal cord. While the authors need not repeat experiments at different segments (although this would be nice!), there should at least be some thoughtful discussion about this shortcoming.
2. Time: The authors use a 10 fps camera, limiting their imaging to 100 ms frames. Of course, events are much faster than this, so the "averaging" over 100 ms may diminish or even miss some events. It would be good to know where the first synaptic events occur. Again, while it would be nice to have a look at a higher frame rate, I think that more fully discussing this shortcoming would be sufficient.
Other major concerns: 3. Previous studies of relevance: The main study that is missing is one from the Jordan lab, where that group used field potential mapping in the cat spinal cord to study where descending locomotor signals arrived. I really think this is of major importance to the current manuscript, and that the results should be compared. The Jordan group used a technique with much faster time resolution (electrophysiology) than calcium imaging, and explored 4 segments in the cat spinal cord. (See PMID: 7891162) There are other relevant cat studies relegated to the history books, many of which are cited here. But the authors state that previous studies have only stimulated "broader areas of the MRF" (lines 382-383). This is not accurate, as microstimulation studies in the cat have nicely demonstrated the Gi as being a locomotor-initiating site. Perhaps the senior author remembers the amazing videos shown by Shigemi Mori of such studies in intact cats presented at the Wenner Gren meeting in 1985? (See PMID: 2611678.) This also brings up another point: there seem to be some interspecies differences, given the more medial sites important in the cat (see also Noga's work) and the more lateral regions (CVL/LPGi) in the mouse. It would be good to have some discussion about this issue. (Interestingly, note also that the "several seconds" to initiate locomotion in the mouse (lines 479-480) is also the case in the cat.) And this leads me to the issue of the Pontine Locomotor Strip, which it seems the authors have identified in the mouse. Early work in the cat from several labs (I can recall Jordan, Garcia-Rill, and maybe Mori as well as Shik, Orlovskii et al) supported that this was a polysynaptic pathway, with distributed synapses including in the cervical cord (Russian group in my memory, but it was a long time ago). The PLS was thought to be located near nV/Vsp, so it fits with the work presented here. But I don't think it's necessary to say that it functions through the LPGi/CVL (lines 402-403), given the cat data (which the authors may want to discuss a bit more?).
4. Stimulation sites. In addition to the above comment about CVL/LPGi vs Gi and possible species differences, I am struck by the result (line 88-89) that the CVL is a stronger site than the LPGi. Two questions here: (a) how does that fit with the data from the Arber lab, which points to the LPGi? And (b) The CVL is closely associated with the pre-Bötzinger complex, a key respiratory centre… given relationships between respiration and locomotion, is this relevant and is it something that should be discussed? (E.g. could this centre be to coordinate the two, such as ensuring that expiration occurs at the biomechanically advantageous point of foot fall?) 5. The explanations sometimes go beyond the data. There is really no reason to over-interpret cause and effect, as the data are excellent as they are. In their concluding remarks, the authors hit the nail on the head (and the tone), and this view should be expressed throughout the manuscript rather than trying to make too much of the data. Specific examples include:  Line 133, "the final descending command signal" -I would agree that this is "a" descending command signal for locomotion, but to say it's "the" pathway means that there are no others (e.g. what about multisynaptic pathways, see PLS point above?).
 The descending command leads to activity in excitatory and inhibitory neurons, and their location is well defined in this study. Furthermore, the argument is nicely made that the synapses with glutamatergic neurons are key. But to say that the descending command is "executed by" (line 232) these modules goes a bit beyond… maybe the descending command must go to both excitatory and inhibitory neurons for locomotion to be effected, for example?  Lines 234-235 -first part, facilitating rhythm generation, okay. But how do we know that the "modules" work together?
 Lines 377-378 are really too much. The "how" is not addressed here. To understand how it's transformed, we need to understand the specific cells that it's activating, the intrinsic properties of those cells, and their integration with specific circuits used to generate the rhythm. Same as the "how" in lines 490 and again in 491 (which should be "where" not "how").  7. Locomotion: given that the cord was cut at L3/4, it's hard to define the rhythmic activity as "locomotion" per se, in which you need alternating activity in flexor and extensor motor neurons. That is, while I think it's okay to use the term most of the time as the evidence is good, I think this caveat should be expressed at the outset. 8. Standard error of the mean: This is a completely useless number and should be eliminated from all figures. In biology, we're interested in variability, not where a "true" mean is. As such, at minimum, the standard deviation should be shown. Better would be box-whisker plots with medians, interquartile ranges, etc. 9. Modules: I think it's okay to use this word. I'll just point out that I think to many (or at least to me), the word refers to particular microcircuits (see, e.g., El Manira zebrafish work), which weren't studied here (i.e. not at the neuronal level). So while I would go for the word "regions" here, it's up to the authors.

Minor:
One general, minor comment that does not need a response. The 5HT work was very interesting. While I think most investigators would say that the descending command is glutamatergic (as the authors cite), many would say that 5HT plays an important auxiliary role. As such, Suppl fig 3 is very interesting in that there does not seem to be a modulating effect. It would be interesting, one day, to stimulate LPGi and add 5HT blockers! 1. Title: Grammatically incorrect, and should read "Deconstructing" for example.
2. Introduction, 1st paragraph. The term "executive" is incorrect. When it comes to the CNS, executive function involves higher cognitive thought, and I don't think the authors mean that's what the spinal cord is doing. I think they mean, perhaps, "executing." Also in line 154.
3. Line 42, remove "that" 4. Line 102 -locomotor efficiency, and locomotor index in the figure -I cannot find how efficiency was defined, or how index was calculated.
6. Figure 2n is not clear, and the legend doesn't help much. Could be improved. 7. Perhaps it's simply my lack of expertise, but the authors are suggesting repeatedly that calcium signal can be seen in descending axons. How does this work? How is the calcium entering? I suppose that these RSN axons have calcium channels (what kind, for what?) at their nodes of Ranvier, or are perhaps still unmyelinated at this age? It might be nice to add a couple of statements about this somewhere. Has a similar finding of Ca activity in long axons been previously described? 8. Line 220, "slower onset" should be quantified 9. Line 259: when reading this, one wonders why it takes 100 ms. Much later, it becomes clear that that's the time resolution of the experiments. Best to mention that here so the reader can interpret. 10. Lines 349-350 -just a comment about some preps vs others -this could reflect the clustering of these neurons in the rostro-caudal dimension, and sometimes you don't hit the clusters? No response needed.
11. Line 353 -not clear how the authors can say definitively that these are "non locomotor initiating"?
12. Lines 389-390: "without having to penetrate tissue" is a false argument. Penetration does little harm, and certainly much less than lopping off rostral regions! 13. Line 395: "impossible" is a pretty strong word 14. Line 438, maybe concurrently instead of coherently? Methods: 1. Dissection -temperature of recordings should be indicated 2. Lines 585-586, verifying level of the cut -this isn't clear at all. How?
3. The nonparametric tests were not defined. When and how often were the data normally distributed?

Response to referees
We would like to thank all reviewers for their insightful and positive comments about our work. We have performed a thorough revision of our manuscript and added new data analysis and experiments to support our conclusion as outlined in detail below.
Reviewer #1 (Remarks to the Author): The paper by Hsu, Bertho and Kiehn uses population Calcium imaging of the L3-L4 lumbar segment to describe the locomotor activity induced by bainstem stimulation. I find the results interesting and important. In particular, the identification of a very localized brainstem region that can evoke locomotion is very impressive and it will certainly prompt further studies aimed at identifying the neurons involved. The Calcium imaging experiments extend throughout the spinal cord section, but of course the price to pay is the loss of cellular resolution. These days, 2-photon Calcium imaging of an entire spinal section has become technically possible, but certainly not mainstream enough to be implemented in any lab, so while one would dream of seeing these very same experiments performed at cellular resolution, the authors do a great job at extracting all the information from the technique they employ.
I really liked the paper and my only comments are requests for more information, because I am of the opinion that some of the data could have been reported better. Also, the methods section lacks some simple, but important detail, that I would ask the authors to add.
We are happy that the reviewer likes our manuscript. We have added quantification of anatomy data and performed new experiments to clarify the issue about glutamate calcium signal in motor neurons as outlined below. We have also thoroughly discussed our choices of recorded lumbar segment.
Main comments: Lines 151-159: I see the logic for performing CtB injections, but a few more details would be needed. It says three were n=11 CTB+ neurons, from N=3 animals, I suppose (2d). Then the same numbers n=11, N=3 are reported for CTB+/VGlut2+ neurons (2e) and again n=11,N=3 for CTB+/TPH+ (2f) neurons. I suggest to look again at the numbers, provide a breakdown of the number of CTB+, VGlut2+ and TPH+ neurons in each of the 3 animals. Also, Vglut2+ and TPH+ should also be expressed in relation to the total number of CTB+ neurons, as I assume that not all CTB+ cells are also Vglut2 (or TPH) The reviewer is absolutely correct. We did not provide these data in a comprehensive way. We have added new data with RNAscope® in situ hybridization to show the expression of Vglut2 and serotonergic cells in the region. These data show nicely the localization of Vglut2 + and Sert + (serotonergic) cells in LPGi/CVL compared to our previous in situ hybridization with immunochemistry data (Page 6, Line 151-153).
Next, we have now reported the CTB data as suggested by the reviewer with clear data from 2 animals instead of 3. Because of the relatively faint YFP expression, we expect that there should be a higher co-localization of Vglut2 and CTB cells than we are able to detect. However, the conclusion remain the same: glutamatergic and serotonergic reticulospinal neurons are located in the LPGi/CVL area (Page 6, Line 165-171).
Line 198: It is stated here (and in methods) that the spinal cord imaging was done at lumbar segment 3/4. I understand the logic behind this choice, to include the most 'rhytmogenic' region (L1-2). However, I am wondering whether the fine temporal and spatial sequence of activation showed in figures 4-6 for glutamatergic and figure 7 for inhibitory neurons, is conserved across segments. In particular, I understand that imaging above L3-L4 would risk damaging the CPG, but I think it would be important to know if a similar observation (both the localization of the signal of figure 4 and the sequence of activation of figure 6) could be done at the L5 level. The imaged region is a 'neither flexor/nor extensor region in terms of motoneurons at least. Even though we do not know much about the rostrocaudal organization of the CPG, observing a similar hierarchy of activation also at the L5 level would be important. Not observing it, would be even more important and would highlight the need of looking also closer to L2. We understand the point about conservation of the pattern throughout the extend of the lumbar spinal cord (L1-L6) that contains the elements of CPG for hindlimb locomotion. This is also a point that is raised by reviewer 3 who want us to discuss this issue but not performing further experiments. We were careful in our choice of the segments because from previous experiments we know (and this is well known in the field) that if we damage L1-L2 the rhythmic activity tends to disappear. But we also know that L3 and caudally located segments can generate a rhythm in isolation form L1-L2 (see Kjaerulff and Kiehn 1998; Kjaerulff and Kiehn 1996; Hagglund et al. 2013). We therefore choose 'L3-L4' in close proximity to L1-L2. We did not systematically investigate the hierarchy of activation at the level of L5. We do agree with the reviewer that it would be interesting to have such experiments in the future. However, these experiments are cumbersome and will take a long time to perform, and we are not sure that they are needed for this study (See also comments from reviewer 3). We, therefore, have not done those experiments. In acknowledgment of the issue we have, however, now added a discussion (Page 20-21, Line 526-540) of the distribution in the lumbar region with also includes a comparison with data from the brilliant Jordan paper 1995 that studied the effect of a descending signal from MLR stimulation in the cat spinal cord.
Lines 260-261. It is stated here that the iEM remained active throughout the stimulation period. Was this activity rhythmic or tonic? From what I see in figure 3e, activity seems rhythmic. In general, I understand the choice of format of figure 4b,d,f, but I think that a format like that of figure 3e would be more informative. We might not have been clear enough about this point. But iEM is first tonically active in the initiation phase and then switch immediately to rhythmicity in the sustained rhythmic phase (see Fig. 3e and g). We have maintained the representation in Fig. 4.
Lines 275-282. It is stated here that the signal from motoneurons in ChAT-GCaMP mice is more ventrally located and smaller than the 'prM' area in the VGlut2-GCaMP experiments. Comparing Suppl. Figure 5h and Supplementary Fig. 8 and the text reads as below. Page 12, starting line 288: " The close proximity of the premotor module to the motor neuron pool and the fact that Vglut2 has been shown to be expressed weakly in motor neurons 50 raise the possibility that at least part of the signal in the prM module could be from motor neurons. To further qualify this conjecture, we performed Ca 2+ imaging in Vglut2 Cre ; R26R GCaMP6f mice while we antidromically activated motor neurons by ventral root stimulation (4 Hz, pulse duration 200 µs, 10 s, 120-300 µA) on one side of the cord with simultaneous recording of the ventral root activity on the other side of the cord at the same segmental level. Under aCSF perfusion, ventral root stimulation might evoke bilateral rhythmic activity 51 because of release of glutamate from central motor neurons collaterals 50, 51 . As an indication that the ventral root stimulation indeed activates the motor neurons on the stimulated side, we found activity in the contralateral ventral root which sometimes was rhythmic. A clear Ca 2+ signal was present in the intermediate area around the central canal with a weaker signal close to or in the motor neuron pools ( Supplementary Fig. 8 a-d, N=3). When nicotinic receptors and glutamatergic receptors were blocked − thereby isolating the antidromic stimulation to the motor neuron pool (by removing any effect of central motor neuron collaterals on spinal circuits) -there was no calcium signal in intermediate area and only a very weak calcium signal in the stimulated motor neuron pool ( Supplementary Fig. 8 e-i, N=3). These data demonstrate that while motor neurons indeed give a weak ventrally located calcium signal in Vglut2 Cre ; R26R GCaMP6f -the contribution of this signal is minor and negligible to what we call the premotor module (prM). We also performed calcium imaging in ChAT Cre ; R26R GCaMP6f mice. " Methods: I find that there are a few procedures that are not fully explained in the methods. I list below the parts that I find lacking, but these will just require adding a few more details. 1) Spinal cord and brainstem sectioning: how were the cut performed? Vibratome? Blade? Also, when moving through more caudal brainstem section, was the sequential cuts performed on the same preparation? We have provided a better explanation of the methods (Page 23, Line 635, 641) to answer these questions. 6) Please define oscillatory index: is it the peak to trough distance in the correlation coefficient? Also, please define the exact formula of the auto-correlation coefficient, because from plot 5c it looks like it is defined between [-1,1] Explanation was given in the Method and is now expanded on Page 25, Line750-754. The formula is from a commercially available software -Clampfit -and is standard.

Minor
Line 112 Should be 'corresponds to' rather than 'corresponding to' Text is now changed (Page 5, Line 117).
Line 169 'serotoninergic neurons do not initiate locomotion' and I would add 'nor modulate it', as shown in Suppl. 3b, that is quite interesting (and to me, a bit unexpected) Changed as requested (Page 7, Line 183-184).

Reviewer #2 (Remarks to the Author):
General Comments: This manuscript describes an interesting and elegant description of the spatiotemporal organization of spinal modules involved in the transformation of tonic drive from descending regions of the brainstem into rhythmic activity in the spinal locomotor network. Overall, the work was received with enthusiasm, and it provides a roadmap for future work. Some weaknesses were identified, including a better rationale for unilateral stimulation and lack of control experiments related to electrical microstimulation, that, if addressed, will strengthen the manuscript.
Thanks for the positive stroke. We have addressed the issues raised by clarifying the text and additional analysis.
Major Comments: • The rationale for using unilateral stimulation is lacking and needs to be better articulated. Thanks for this comment. We envisaged that it was more straightforward and readily understandable to use unilateral stimulation and mapping as it has also been done traditionally in brainstem mapping experiments. With the active site in hand it also turn outs that unilateral (as has also been known for years of MLR stimulation) induce bilateral locomotion. Moreover, we find that the unilateral stimulation leads to a slight asymmetric activation of the spinal locomotor networks which was advantageous for our analysis since we could follow the signal travelling from the ipsilateral side in the cord to the contralateral. We have clarified our rational on Page 3, Line 86-88.
• Line 8: The use of the term "whole brain screening" is misleading and implies that more areas were examined than what was reported. A more accurate statement is "whole brainstem screening". The reviewer is right. It should not be whole brain screening but "whole brainstem screening". Text is now changed (Page 1, Line 8).
• Lines 70-71: There is a lack of control experiments to support the authors assertion that lower intensity microelectrical stimulation (mES) restricts activation of smaller regions of the brainstem than does broader, more intense stimulation. Although this assertion is reasonable and likely, control experiments supporting this are suggested. Simply, one could express GCaMP6f in a pan-neuronal transgenic line and monitor/measure the spread of calcium signals with different stimulation parameters in the presence of TTX to abolish fast synapses. One predicts that the lower intensity mES will activate and spread across a smaller/more restricted region of the transverse cord. For example, mES of serotonergic region of transverse brainstem produced rhythmic spinal locomotor activity (Fig. 2h), which suggests that mES is not as restrictive as implied (this is a misunderstanding). Thus, there is not sufficient evidence to support the statement that mES is confined to the LPGi/CVL region (lines 179-82). When we referred to intense stimulation in previous locomotor experiments in the rodent: they used 1 mA which 10-50 times stronger than the stimulus strength we used. The minimal threshold strength we use is 20-30 µA similar to brainstem mapping experiments used by Glover and Perreault (2008, 2011, 2014. They estimated a current spread from the tip of electrode to be around 200-300 µm at 40 µA. The same calculation could apply to our experiments. Importantly, we carefully mapped the stimulation from the surface by visually placing the stimulation electrode in equidistant points in a matrix covering the entire surface of the cut brainstem. Close to (~350 µm) active points we found inactive points which shows the current did not spread to the active points. Based on these arguments we retain that our stimulation protocol is reliable and with internal points inactive points as control.
However, to further address this issue we have performed extra experiments as suggested by the reviewer using the Vglut2 Cre ;R26R GCaMP6f mouse line and measuring the calcium change in the brainstem after blocking glutamatergic collaterals with KA. These experiments are presented in Supplementary figure 1 along with text edits (Page 2-3, Line 71-77). They show that there is limited calcium activation (~350 µm) around the electrode at low current amplitudes. The spread increases with higher intensities. We therefore retain that there is evidence to support the statement that mES is confined to the LPGi/CVL region.
Minor Comments: • Title: Grammatically incorrect and suggest either "Deconstruction of the modular…" or "Deconstructing the modular…". Thanks for pointing it out. Title is now changed.
• Lines 122-23: The callouts to Fig. 1n for the left and right panels are reversed (lefttime-frequency plot; right -circular plot). Thanks for pointing out. Texts are now changed (Page 5, Line 137-138).
• Lines 156-57 and Fig. 2: Panel e shows (labeled) colocalization of TPH and CTB, while panel f shows (labeled as) colocalization of Vglut2 and CBT, so it is necessary to confirm which subpanel goes with which callout. Thanks for pointing out. Texts are now changed (Page 6, Line 168 and 170).
• Lines 275-77: Please edit the sentence to reflect that calcium signal was monitored in spinal neurons but not in the ventral roots (as it is written). Extracellular recordings monitored activity in ventral roots. Text edited as requested (Page 13, Line 307-309).
• Line 336: Suggest to callout to Figure 3e regarding IEMi being the first rhythmic module. Text edited as requested (Page 16, Line 369).
• Lines 345-47: Provide the number of preparations that showed calcium signal in the ipsilateral lateral funiculus in response to LPGi/CVL stimulation in KA and mephenesin. We now have provided the requested number (Page 16, Line 379-380).
• Lines 347-49: Provide the number of preparations that showed calcium signal in neurons close to the central canal in in response to LPGi/CVL stimulation in mephenesin. We now have provided the requested number (Page 16, Line 380).
• Figures 1 and Supplementary Figure 1: The sagittal cuts located at 12N in Fig. 1 are listed as "12NR" and "12NC", whereas the same cuts in Supp. Fig. 1 are listed as "12-1" and "12N-2". So, the reader must assume which cuts are analogous in the two figures… please clarify.
Thank you for point this out. Texts are now clarified in the figures.
Reviewer #3 (Remarks to the Author): In this manuscript, Hsu et al describe their work outlining a descending locomotor command from a specific brain stem reticulospinal area, the CVL/LPGi, to the midlumbar spinal cord, where the tonic descending signal is converted to a rhythmic signal to produce locomotor-like activity. They are addressing an important question -one that will be of great interest to the community studying locomotion. In addition, they use a broad range of techniques, and demonstrate the use of those techniques to understand connectivity between distant regions of the nervous system. Furthermore, the study is well organised and logical, and beautifully illustrated. As such, I am very enthusiastic about it.
Nonetheless, I have a few major concerns. I hope the authors read this in light of my enthusiasm and don't get discouraged by the length or number of my comments!
We would like to thank this reviewer for very insightful comments. The reviewer is right in most issues raised. We have as requested added discussion points and clarifications to all request as outlined in detail below.
The manuscript is looking at the initiation of locomotion in the neonatal mouse over space and time. There are issues about both that the authors should consider addressing: 1. Space: The authors are looking at a single segment in the lumbar spinal cord, L3/4. It is not clear why they selected this segment, and how the results would have differed, and the implications of those differences, had they looked elsewhere. For example, in the senior author's earlier work in the neonatal rat, the suggestion was made that the key region was in the more rostral lumbar spinal cord. While the authors need not repeat experiments at different segments (although this would be nice!), there should at least be some thoughtful discussion about this shortcoming. We understand the point about conservation of the pattern throughout the lumbar spinal cord (L1-L6) that contains the elements of CPG for hindlimb locomotion. This is also a point that is raised by reviewer 1. We were careful in our choice of the segments because from previous experiments we know (and this is well known in the field) that if we damage L1-L2, the rhythmic activity tends to disappear. But we also know that L3 and caudally located segments can generate a rhythm in isolation form L1-L2 (see Kjaerulff and Kiehn 1998; Kjaerullf and Kiehn 1996; Hagglund et al. 2013). We therefore choose 'L3-L4' in close proximity to L1-L2. We did not systematically study the hierarchy of activation at the level of L5. We do agree with the reviewer that it would be interesting to have such experiments in the future. However, these experiments are cumbersome and will take a long time perform. We therefore have not done those experiments. In acknowledgment of the issue, we have now added a discussion of the distribution in the lumbar region with also includes a comparison with data from the brilliant Jordan paper 1985 that studied the effect of a descending signal from MLR stimulation in the cat spinal cord (Page 20-21, Line 526-540).
2. Time: The authors use a 10 fps camera, limiting their imaging to 100 ms frames. Of course, events are much faster than this, so the "averaging" over 100 ms may diminish or even miss some events. It would be good to know where the first synaptic events occur. Again, while it would be nice to have a look at a higher frame rate, I think that more fully discussing this shortcoming would be sufficient. We already had some discussion of this issue in the current version of the manuscript where we clearly stated that we cannot determine monosynaptic latencies based on these frame rates (Page 20, Line 507-520) but that the pharmacology allow us to that Other major concerns: 3. Previous studies of relevance: The main study that is missing is one from the Jordan lab, where that group used field potential mapping in the cat spinal cord to study where descending locomotor signals arrived. I really think this is of major importance to the current manuscript, and that the results should be compared. The Jordan group used a technique with much faster time resolution (electrophysiology) than calcium imaging, and explored 4 segments in the cat spinal cord. (See PMID: 7891162) The reviewer is right. It is a mistake that we did not discuss and compare our data with this extremely nice study form Larry Jordan. We now give full credit to the cat study and discuss the similarities and differences to our study on Page 20-21, Line 526-540. This also brings up another point: there seem to be some interspecies differences, given the more medial sites important in the cat (see also Noga's work) and the more lateral regions (CVL/LPGi) in the mouse. It would be good to have some discussion about this issue. (Interestingly, note also that the "several seconds" to initiate locomotion in the mouse (lines 479-480) is also the case in the cat.) We recognize that the optimal locomotor site is in Gi in cats, and we now refer to those papers directly and discuss the differences to the mouse (Page18, Line 436-441). We are quite aware that there are "several seconds" to initiate locomotion also in the cat and also give references to the manuscript (Page 20, Line 521-525).
And this leads me to the issue of the Pontine Locomotor Strip, which it seems the authors have identified in the mouse. Early work in the cat from several labs (I can recall Jordan, Garcia-Rill, and maybe Mori as well as Shik, Orlovskii et al) supported that this was a polysynaptic pathway, with distributed synapses including in the cervical cord (Russian group in my memory, but it was a long time ago). The PLS was thought to be located near nV/Vsp, so it fits with the work presented here. But I don't think it's necessary to say that it functions through the LPGi/CVL (lines 402-403), given the cat data (which the authors may want to discuss a bit more?). We are happy that the referee recognizes this and agree with us -we indeed already referred to PLS in our previous version. We now add two new references to this work in the paper from Mori and Shik (1977 and 1978). The reviewer is right that there is a possibility that the PLS does not act through LPGI/CVL and we just block a polysynaptic pathway. This does not change our conclusion, but we have included this interpretation as well on Page 18, Line 424-432. " Indeed, we show that non-cell-specific micro-electrical stimulation of the lateral medulla along the rostrocaudal levels evokes locomotor bursts, with a locomotor-like pattern. These areas form a strip, which corresponds to the previously identified pontomedullary locomotor strip, a descending tract that evokes locomotion in cats 15, 17, 65-68 . However, the electrically induced locomotor-like bursts were absent or largely diminished after blocking the collateral glutamatergic activity in the brainstem and upper spinal cord, suggesting that these areas mediate their effect through collaterals in the brainstem, possibly acting through the LPGi/CVL or through other polysynaptic relays in brainstem or upper spinal cord." 4. Stimulation sites. In addition to the above comment about CVL/LPGi vs Gi and possible species differences, I am struck by the result (line 88-89) that the CVL is a stronger site than the LPGi. Two questions here: (a) how does that fit with the data from the Arber lab, which points to the LPGi? We have changed the text to comment on this issue. Page 19, Line 453-459: " Nevertheless, the convergence of LPGi in neonatal and adult mice suggests that LPGi is ontogenetically preserved for locomotor initiation. However, we have also found that the locomotor-initiating area includes CVL in the neonatal mouse. This apparent difference between neonatal and adult mice may reflect developmental changes. Nevertheless, because of the intact glutamatergic transmission in the brainstem in adult mouse experiments it seems difficult to completely exclude a contribution from CVL even though it was not stimulated directly. " And (b) The CVL is closely associated with the pre-Bötzinger complex, a key respiratory centre… given relationships between respiration and locomotion, is this relevant and is it something that should be discussed? (E.g. could this centre be to coordinate the two, such as ensuring that expiration occurs at the biomechanically advantageous point of foot fall?) We are not experts on pre-Bötzinger complex. But we think that the pre-Bötzinger complex is located a bit more caudal than the CVL (Ruangkittisakul…Del Negro, 2014, PMID: 25138790) that we identify as a locomotor site. CVL is close to the parafacial respiratory group though, and we mention this in the text now (Page 18, Line 442-445).
5. The explanations sometimes go beyond the data. Yes, we agree -we have toned down the text in the places pointed out by the reviewer. There is really no reason to over-interpret cause and effect, as the data are excellent as they are. In their concluding remarks, the authors hit the nail on the head (and the tone), and this view should be expressed throughout the manuscript rather than trying to make too much of the data. Specific examples include:  Line 133, "the final descending command signal" -I would agree that this is "a" descending command signal for locomotion, but to say it's "the" pathway means that there are no others (e.g. what about multisynaptic pathways, see PLS point above?). Changed to 'a' (Page 6, Line 141).
 The descending command leads to activity in excitatory and inhibitory neurons, and their location is well defined in this study. Furthermore, the argument is nicely made that the synapses with glutamatergic neurons are key. But to say that the descending command is "executed by" (line 232) these modules goes a bit beyond… maybe the descending command must go to both excitatory and inhibitory neurons for locomotion to be effected, for example? We have toned done the text and now replace it with the following texts: (Page 10-11, Line 246-250). "These results demonstrate that the unilateral LPGi/CVL command is received by excitatory spinal modules that leads to the expression of: first a tonic initiation phase during which excitatory modules in the spinal cord are recruited to facilitate rhythm generation, and then in a rhythmic phase in which the modules are active to drive the locomotor-like activity."  Lines 234-235 -first part, facilitating rhythm generation, okay. But how do we know that the "modules" work together? Agree. This is implied from the indirect observation that they are active in different part of the cycle. We have changed the wording slightly (Page 11, Line 250).
 Lines 377-378 are really too much. The "how" is not addressed here. To understand how it's transformed, we need to understand the specific cells that it's activating, the intrinsic properties of those cells, and their integration with specific circuits used to generate the rhythm. Same as the "how" in lines 490 and again in 491 (which should be "where" not "how"). We agree-how is changed to when and where (Page 17, Line 405-406). 7. Locomotion: given that the cord was cut at L3/4, it's hard to define the rhythmic activity as "locomotion" per se, in which you need alternating activity in flexor and extensor motor neurons. That is, while I think it's okay to use the term most of the time as the evidence is good, I think this caveat should be expressed at the outset. We do not think we call it 'locomotion' here. We agree that we only measure flexor related activity. We know from 25 years of experiments with the in vitro preparation that when flexor related roots are active, they are out of phase with extensors which we normally call locomotor like activity because it corresponds to a complex flexor extensor pattern in the hindlimb (Kiehn and Kjaerulff 1996).
8. Standard error of the mean: This is a completely useless number and should be eliminated from all figures. In biology, we're interested in variability, not where a "true" mean is. As such, at minimum, the standard deviation should be shown. Better would be box-whisker plots with medians, interquartile ranges, etc. All the bar graphs are replaced with box-whisker plots according to reviewers' recommendation ( Fig. 1o, Fig. 2o, Fig. 3f, Fig. 5e-f, Supplementary Fig. 6g, Supplementary Fig. 8i, and Supplementary Fig. 10c). 9. Modules: I think it's okay to use this word. I'll just point out that I think to many (or at least to me), the word refers to particular microcircuits (see, e.g., El Manira zebrafish work), which weren't studied here (i.e. not at the neuronal level). So while I would go for the word "regions" here, it's up to the authors. We opt to keep the word modules but are certainly aware of the general discussion.
Minor: One general, minor comment that does not need a response. The 5HT work was very interesting. While I think most investigators would say that the descending command is glutamatergic (as the authors cite), many would say that 5HT plays an important auxiliary role. As such, Suppl fig 3 is very interesting in that there does not seem to be a modulating effect. It would be interesting, one day, to stimulate LPGi and add 5HT blockers! Thanks for this comment -we agree and will keep it in mind.